Kaufman et al: Obstructed by Thompson and Jacoby

A CA reader sent me an email, noting the following entry in minutes of a meeting.

M Loso inquired about Lonnie Thompson’s ice core data. These data are not presently available but will be investigated by Caspar.

This comment is minuted in a meeting of PIs leading up to Kaufman et al 2009 – a meeting of no fewer than 28 people (sponsored by the US National Science Foundation.) The minutes are online here. It would be highly interesting to see Ammann’s report on the Thompson obstruction. A novel role for the Texas Sharpshooter. Caspar Ammann, PI (Private Investigator). I wonder how thorough his investigation was.

Later in the meeting, they discuss the “High Canadian Arctic”, where they comment:

Tree-ring sites from Jacoby might be of use. R[ob] Wilson might have longer tree-ring records but needs to check with D-Arrigo

Yes, of course, tree ring sites from Jacoby might be of use.

Both of these problems – Thompson failure to archive and Jacoby’s incomplete archiving – have been repeatedly publicized at Climate Audit. See the Thompson category for prior discussion of Lonnie Thompson. The Alaska ice core in question is, of course, the Bona-Churchill, Alaska ice core, drilled by Thompson in 2002, press releases issued, AGU notice and then dead silence. A few years ago, I speculated that this dead silenced presaged “bad” drill results – “bad” in the sense that the drill results did not show that things were “worse than we thought”. Indeed, I speculated that the Bona-Churchill drill results would show that delO18 went the “wrong way” in the 20th century at this ice core. Bona-Churchill remains unpublished to this day, but there was a graphic in a workshop showing that Bona-Churchill delO18 did, in fact, go the “wrong way” as reported at CA here. So in case, Caspar Ammann PI didn’t report to Loso on Lonnie Thompson’s ice core, Loso can at least consult the above CA post.

Jacoby’s incomplete archiving has also been a topic of commentary here. In this case, unlike Thompson, Jacoby has archived a lot of tree ring measurements. The frustration is that he hasn’t consistently archived all the sites. Problems with Jacoby archiving were the topic of one of the very first CA posts here. In the influential Jacoby and D’Arrigo NH treeline reconstruction, they reported that they had collected cores from 35 sites, using 10 plus Gaspe in their reconstruction. I asked Climatic Change to require Jacoby to provide the data for the 24 sites collected, but not reported in the paper. Jacoby’s response needs to be read in full, but is excerpted below:

The inquiry is not asking for the data used in the paper (which is available), they are asking for the data that we did not use. We have received several requests of this sort and I guess it is time to provide a full explanation of our operating system to try to bring the question to closure.

…

We strive to develop and use the best data possible. The criteria are good common low and high-frequency variation, absence of evidence of disturbance (either observed at the site or in the data), and correspondence or correlation with local or regional temperature. If a chronology does not satisfy these criteria, we do not use it. The quality can be evaluated at various steps in the development process. As we are mission oriented, we do not waste time on further analyses if it is apparent that the resulting chronology would be of inferior quality.

If we get a good climatic story from a chronology, we write a paper using it. That is our funded mission. It does not make sense to expend efforts on marginal or poor data and it is a waste of funding agency and taxpayer dollars. The rejected data are set aside and not archived.

As we progress through the years from one computer medium to another, the unused data may be neglected. Some [researchers] feel that if you gather enough data and n approaches infinity, all noise will cancel out and a true signal will come through. That is not true. I maintain that one should not add data without signal. It only increases error bars and obscures signal.

As an ex- marine I refer to the concept of a few good men.

A lesser amount of good data is better without a copious amount of poor data stirred in. Those who feel that somewhere we have the dead sea scrolls or an apocrypha of good dendroclimatic data that they can discover are doomed to disappointment. There is none. Fifteen years is not a delay. It is a time for poorer quality data to be neglected and not archived. Fortunately our improved skills and experience have brought us to a better recent record than the 10 out of 36. I firmly believe we serve funding agencies and taxpayers better by concentrating on analyses and archiving of good data rather than preservation of poor data.

In the older posts, you’ll also see correspondence with Jacoby and d’Arrigo about the Gaspe update – the Gaspe series used in MBH98 has a huge HS, but an updated version did not have one. The Gaspe update was never reported. Despite their failure to report the update, I became aware of the existence of the update (and had a graphic of it); but when I requested the data, it was refused on the basis that that it did not give the right signal. See http://www.climateaudit.org/?p=182.

In 2005, I tried to get the NSF to intervene and require Jacoby to archive his data completely. They refused.

Thus, several years later, not just me, but young Arctic scientists are frustrated by data obstruction by Thompson and Jacoby. Unfortunately, these young scientists are unable or unwilling to record these frustrations in public and the records remain incomplete to this day.

The greater fault lies with the acquiescence of senior scientists and senior institutions. The US National Academy of Sciences was asked by the House Science Committee to look at this problem in climate science. Instead of providing any useful reports, two consecutive panels refused to look squarely at the problem, merely re-iterating platitudes that had been agreed to 20 years ago. The fault also lies with senior climate scientists who have likewise failed to speak out. It’s an issue that realclimate should have been able to agree with climateaudit. realclimate has an opportunity and a forum to speak out against data obstruction by Thompson, Jacoby etc, but have never risen to the challenge. Nor for that matter have other senior climate scientists uninvolved in the blogosphere – there’s nothing to stop Jerry North or Kerry Emanuel or Carl Wunsch or people like that from writing to Thompson and Jacoby and others and asking them to mend their ways.

Unfortunately the problem remains to this day. And here we have an example where it is not simply Climate Audit objecting to the data obstruction, but young field scientists trying to respond to the public desire for improved Arctic proxies.

There are many other interesting aspects to the minutes of this meeting, other PI meetings and indeed to the entire process leading to Kaufman et al 2009, which I’ll discuss on another occasion.

It seems to me that they have skated past this issue with relatively little controversy outside the “climate science” community. Perhaps there will be a breakthrough, but it appears more likely that Thompson and Jacoby will retire unscathed with their data unarchived.

It took the retirement of the geosyncline camp for plate tectonics to be fully accepted. When I was an undergrad in the mid to late 70’s some of my profs still thought it relevant to teach it as an “alternative” view.

As the younger generation collects their own data the whole truth will come out. In the mean time these younger researchers still need to be made aware of the big holes in the record and the obfuscation of their older peers in filling those holes when the data they have already collected doesn’t agree with their published record or pet theory.

DK [Darrell Kaufman] suggests, at first pass, to include all records so we do not “cherry-pick” records. Latter screening will inevitable reduce the number of records

This reflects is a legitimate, but difficult problem: On the one hand, you want to include all records that are not tainted by a specific problem (like stripbark or human effect on varves), but on the other hand, you may quickly run out of DOF when you have more records than temperature observations.

When correctly done (in contrast to MBH), PCA may be the way to go here. However, in order to avoid “PC-picking”, there must be a rule that if PC(k) is to be included in the calibration equation, PC(1) – PC(k-1) must also be included, and the hypothesis that all k have zero coefficients must be rejectable with an appropriate F or chi-square test. Thus, you may not pick PC(5), for example, because of its high t-stat, and skip over PC(1) – PC(4).

“Screening” the records (or PCs) by their correlation with temperature or whatever, as suggested by Kaufman above, invalidates the p-values of their apparently high t-stats.

Re: Hu McCulloch (#8), “However, in order to avoid “PC-picking”, there must be a rule that if PC(k) is to be included in the calibration equation…”

Temperature sensors can be calibrated against a known standard, in order to be of use recording a temperature series. One may even try calibrating an old sensor under a variety of use conditions in order to evaluate the likely precision of an old uncalibrated temperature series.

One can pass a PC analysis through a physical theory in order reconstruct a signal of interest that is convolved with other signals within a single measurement. For example, if one knew the temperature and precipitation history of a locale, one might use PCA to analyze a local O-18 record, express the d(O-18) as a function of temperature, precipitation, and monsoon trajectory, all in the analytical terms of a valid physical theory and, knowing the temperature and precipitation and their physical interrelationship, finally extract the monsoon record by a suitable weighted combination of the PCs, with the PC weights determined by physical theory.

Principal components are numerically orthogonal. They are not physically orthogonal. As such, all principal components derived from any measurement set of complex physical phenomena are convolutions of multiple physical signals. The PCs are not physically orthogonal even if any one of them can be statistically correlated with some independent physical measure. To give the barest physical credibility to this sort of associational correspondence, one would have to show that no other associations with any other physical measure can be found. I.e., no association of the PC of interest with, e.g., the Dow Jones 500, bra sales, trends in salinity, or the incidence of autism.

In short, finding a statistical >0.5 correlation between a given PC and temperature is not a “calibration.” Claiming such is an abuse of a scientific term that otherwise has an explicit meaning: comparative test of sensor output with a known and explicitly relevant standard.

Just because someone has come along and made a qualitative judgment that some series is “temperature limited,” does not mean that PC1 is a measure of temperature. PC1 merely contains the largest set of numerically orthogonal points that can be extracted from the data set. That’s it. It’s a mixture of signals unless otherwise shown by physical theory. There doesn’t exist a statistical method that can extract or produce physical meaning. Not one. There is no such thing as a statistical “calibration equation.” There are only physical calibrations.

The entire business of proxy thermometry is a crock, a whole crock, and nothing but a crock. So help me, whomever. If climate scientists need statisticians to help them get the statistics right, statisticians need the reciprocal help of scientists to get the science right.

So, here’s a free consult for all the statisticians out there, from a practicing experimental physical scientist: Physical meaning can only be assigned within a physical theory. There is no such thing as a statistical calibration equation. Principal components have no physical meaning whatever. Physical meaning cannot be assigned by fiat, nor by correlation, nor can quantitative results be statistically extracted from qualitative judgments plus numbers. Just to be fair and complete, quantitative results cannot be extracted from qualitative judgments by any physical method, either.

I’ve commented on this before, and it’s really distressing to see the delusion persist here, of all places, that statistical analysis can grant physical meaning.

Much less eloquently, I’ve said much the same a few times so I’m hardly likely to disagree.

However, in the qualitative realm, if preliminary analysis shows one dominant PC, one might think that there is one dominant physical process and go looking for it. Thus, the PC might have some use in encouraging the researcher to try to do a physical calibration (which he/she should have done in the first place if following the Scientific Method).

If, after this, there is shown to be a strong and simple calibration, there is justification to proceed with the work.

Even at Junior school we were taght layouts with chapter headings like “Aim, Apparatus, Hypothesis, Proposed Experiment, Calibration, Interpretation, Conclusion, References.” I suppose my grandchildren would dismiss this as “Stone Age” as is their want.

However, in order to avoid “PC-picking”, there must be a rule that if PC(k) is to be included in the calibration equation, PC(1) – PC(k-1) must also be included, and the hypothesis that all k have zero coefficients must be rejectable with an appropriate F or chi-square test. Thus, you may not pick PC(5), for example, because of its high t-stat, and skip over PC(1) – PC(4).

This would be a mistake. See, for example, “A Note on the Use of Principal Components in Regression” by Ian Jolliffe. The PCs are ordered according to their contribution to the variance of the “x” variable. But if you’re regressing on them, you’re really interested in whether or not they explain variance in the “y” variable, and there’s no reason to assume these contributions will be the same.

Monday’s lecture is on the Scientific Method. I hope when I am done, even the freshmen will be able to spot what’s wrong with the Jacoby quote above. I’ve picked up so many amazing quotes from CA over the last year for the “How NOT to do science” section that I won’t be able to go over each on in class.

“The criteria are good common low and high-frequency variation, absence of evidence of disturbance (either observed at the site or in the data), and correspondence or correlation with local or regional temperature.”

Obviously not a believer in teleconnection then. I wonder what Cherry Jacoby would have to say to Mann about the inclusion of bristlecones and Tiljander lake sediment in particular in his proxy studies.

NSF is subject to FOIA requests. Has anyone considered filing a FOIA request to the NSF for the data that was gathered based on NSF funding? The NSF Grant Policy Manual clearly states: “Investigators are expected to share with other researchers, at no more than incremental cost and within a reasonable time, the primary data, samples, physical collections and other supporting materials created or gathered in the course of work under NSF grants. Grantees are expected to encourage and facilitate such sharing.”

As the grantees haven’t shared the primary data, a FOIA may facilitate such sharing.

If the data are not forthcoming, a FOIA requesting all documentation of why NSF is not requiring its grant recipients to share their data and why the NSF is still funding grant recipients who do not abide by the terms of NSF Grant Policy Manual would be in order.

If we get a good climatic story from a chronology, we write a paper using it. That is our funded mission. It does not make sense to expend efforts on marginal or poor data and it is a waste of funding agency and taxpayer dollars. The rejected data are set aside and not archived

An entire book could be written about what is incorrect in this statement.

If we get a good climatic story from a chronology, we write a paper using it. That is our funded mission. It does not make sense to expend efforts on marginal or poor data and it is a waste of funding agency and taxpayer dollars. The rejected data are set aside and not archived

An entire book could be written about what is incorrect in this statement.

It could be, but there is no need.

It can be explained in three sentences that are inarguable. The first sentence says that there can be time spans with essentially no authentic, significant temperature differences from year to year. The second sentence says that proxies for temperature change should therefore exhibit insignificant data character over these terms. The third sentence says that there is no logical basis to exclude data that are bereft of character, for precisely the reason that the researcher does not know if it is simply a quiet time.

Alternatively, the objection could be phrased in terms of false positives and their brethren; and logic.

JACOBY: “….. If we get a good climatic story from a chronology, we write a paper using it. That is our funded mission. It does not make sense to expend efforts on marginal or poor data and it is a waste of funding agency and taxpayer dollars. The rejected data are set aside and not archived ….”

TAG: An entire book could be written about what is incorrect in this statement.

The Introduction section of this book would note that in the last forty years, the pressure on government-funded scientific research agencies to produce “useful” products has turned many of their employees away from the objective of doing fundamental research into what the data is actually saying to them — and accepting whatever information is revealed — and towards the objective of using the data as a building block type of resource in manufacturing a product which seems to be worthy of the public funds spent on it.
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Everyone should understand that Jacoby, in his own mind, believes that temperature proxies work as advertised if enough caution is used in their selection. He is not doing research into basic questions, he is doing QA on a developmental analysis product whose function is to produce a useful “climate signal” as his customers in the Global Warming Industrial Complex define it.
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Jacoby and his colleagues have crossed the boundary between the kind of science pursued for purposes of basic research, and the kind of science pursued in support of product development and manufacturing. What these people are doing is actually product development research, and so his statement as quoted above is perfectly consistent with the kind of science he is actually pursuing. (Not that he or any of his colleagues would ever admit to this.)

I think there is a genuine conceptual difference. Mann and Jakoby etc. seem to be looking for trees that are good thermometers, by looking for ring patterns that match up with temperatures. Then they are used further. They don’t seem to be interested in why some trees are better thermometers than others. At least that’s the gist of what I get from them.

Fred2, I think that it is fair to say that some chronologies will make better thermometers than others, but without archiving, who is to know whether the rejected series contain signal or not? Also, if there is so much “noise” that needs to be rejected, how do we know whether archived series are true signal or “noise” leading to false positives?

Well said. The differential equations that describe a particular physical phenomenon have their own set of physical modes that are not related to principal components in any way.
You can fool some of the people ..

Re: Gerald Browning (#22), What impresses me, Jerry, is that so many highly trained physical scientists have either joined the bandwagon, or have remained silent about the obviously shoddy practices of proxy thermometry. And after your expert explanations, one can be equally amazed about the critical negligence that pervades the field of climate modeling.

If you mean this Ken, you misunderstood my comment and reply to Hu M on another thread. I did have a limerick in mind that would have had some fun with your comment and Hu’s, but then you don’t read minds. Do you?

But to the point at hand, I view the response by Jacoby as an indication that he is not aware of the statistical ramifications of his selection process and not showing his rejected data. He sees no need to make a case for the criteria he used in rejecting data.

He is not even contorting what he did by wordsmithing – which makes the silence of others, who one would think should know better, even more puzzling.

Fred2,
I guess it’s not obvious to you what’s wrong with that. Let’s say, for the sake of argument, that tree rings are not good thermometers but that 10% of them randomly correlate to some temperature series. Now let’s say that you as the researcher select a population of trees that your theory says should contain a temperature signal in their rings, so you go out and core a bunch of them. Now if you just use all the cores you collected you will find that the series does not correlate well with temperature so your is nullified. That’s science. You start over. But now suppose that you only select the 10% that actually “contained a signal” (had good correlation). Now you would have fooled yourself that your theory has merit when in fact it does not. This is why data snooping is such a big deal.

So far, what has been the downside of obstructing attempts to obtain data? Basically, nothing except a few blog postings. The unfortunate aspect of human nature is that unless and until there is pain applied, bad behavior, particularly if it profits the person doing it, will persist. This applies from everything to a child raiding the cookie jar, a thief stealing cars, or a researcher refusing to share data (for whatever reason, ego, to shield incompetence (or worse), just plain sloppiness). Not all of the examples are of the same legal or moral seriousness, but they are of the same kind of behavior, and so far no one, not the NAS, no one who matters and can hold their feet to the fire seems to care enough to do something about it. This is also a situation that you want to avoid in auditing, where the people who should be audited and overseen by neutral parties do their own audit, never a good situation.

Until the community stops publishing and paying for research that doesn’t include full disclosure of data and methods, this will not end. Since said research often supports the dominant political meme of the day, don’t expect any support from that side of the aisle either.

correspondence or correlation with local or regional temperature. If a chronology does not satisfy these criteria, we do not use it.

That’s an amazing quote. It would have been more amazing one year ago when I learned of M08 but in this case we have no idea of the number of proxies rejected or kept. You have to be pretty trusting to accept the scribble that’s left over and work more math on it. M08 gave a terrible explanation that a high enough percentage of the pre-hand selected data was kept to verify that the data wasn’t random. In this case to eliminate data in a behind the scenes undefined black box approach … impressive.

The unprecedentedality of reconstructions vanishes if the corrections to GISS and HadCRUT weren’t applied. I’m not saying the corrections are wrong but even a small overestimation of surface trend (especially a sudden one) is substantially helpful to correlation and unprecedentation of reconstructions.

There are potential theoretical reasons why some trees, even of a given species, might be “better thermometers” than others. There’s population variance of genotypes and phenotypes, and that phenomenon can frequnetly be given plausible grounding in evolutionary game theory. But unless there’s a well-thought-out statistical methodology that supports the alternative against the null “all trees (of this species) are equally good thermometers,” then the procedure of simply setting aside poor-looking chronologies just doesn’t fly. I think of cross-sectional time-series techniques, that is for panel (longitudinal) data sets. There are ways to go about testing hypothesis of the kind “There is no heterogeneity over the cross section (the tree cores) in their time-series characteristics (e.g. their correlation through the period of historical climate records with temperatures).” Maybe Steve or someonme else knows whether such statistical tests have been done. I haven’t heard any reference to such a study since I started reading this blog a few months back.

There should be a set of a priori criteria for pre-determining a given sampling project. The decision to archive should be a given based on these criteria. Any information gained from this data is useful – whether there is correlation with the insturmental record or not – as it would shed light on the noise vs signal issue. Sufficient sampling should enable a level of statistical confidence (or lack of) in those series which correlate with temperature.

The questionable backgrounds of the proxy selection process in “team” reconstructions is a strong argument for engineering discipline to be applied on process, procedure, and documentation.

Re: Layman Lurker (#43),
you are making an implicit assumption about what kind of population you are sampling from, and this implicit assumption is what is at issue here. If individual trees are all homogenous in behavior, then every sampled tree is an instance of one type, the homogenous type, in that sampled population. But suppose instead that the population of trees is a mixture of different types (within species). Each distinct type (genotype, phenotype) within the population (species) may have its own signal to noise aspect “as a thermometer.” Then, pooling the data across types destroys potentially useful information that is specific to specific types.

On a more general note, I agree with much of what people are saying here. The researchers in question should obviously archive all of their data. More deeply, they shouldn’t data snoop in the way they are doing. Still more deeply, if you thought that trees were heterogeneous thermometers, then you ought to have some scientific theory as to why and that ought to guide your statistical inquiry about it.

But I have to part company with the implicit assumption that a tree is a tree is a tree. This may be the correct way of thinking in sciences like physics or applied fields like engineering, where you tend to assume that there is but one type of electron or steel plate and it behaves the same no matter where you find it in the universe. But it is usually a mistake in biological and human sciences, where deep heterogeneity of observational units is both empirically real and theoretically expected.

Let me get this straight. We go out and collect a load of data. We “test” it looking for a temperature “signal”. A few data sets show such a “signal”.
Am it being naive here or would a subset of (say) tree ring records, essentially composed of random noise, be bound to contain some that gave an apparent match with modern temperature trends?

Hey presto! It’s a “treemometer”.

Just how many sets of “bad” data did Jacoby et al wade through and discard, before they found their “good” data?

In physics, if you have ‘group of trees’ some of which behave identically one of which does not then the assumption is that there is a flaw in the group not the singleton. IE in any theory or model we are searching for the exception and not the rule because it will tell us where we have the biggest deviation form our model/theory and therefore the limit(s) of them.

Re: stephen richards (#45),
at the most general level of scientific method, there is really no difference between what I think you describe as your practice and what I understand to be my practice. If I am designing an experiment to test a theory, my job as an experimenter is to try hard to kill the theory, and I do that by trying to figure out how to create empirical exceptions to the theory.

RE Pete #29,
Roman found me Jolliffe’s “A Note on the Use of Principal Components in Regression.” It was in Applied Statistics, 1982, vol. 31: 300-303.

Jolliffe’s point in this note is that sometimes a PC that is way down the list, and which explains only a tiny proportion of the variance in the X matrix, is still an important explanatory variable for the dependent variable y.

This may occur, but then it is not clear what function PCA is serving. Why not just use the raw X matrix directly?

PCA is potentially useful in the present context when there are more explanatory variables than observations, or more proxies than observations, as in Kaufman’s case (23 proxies and only 14 decadal observations on temperature). The whole point is to reduce this unwieldy data set down to a manageable number of candidate series, so that there will be lots of DOF (or at least a small but positive number, in Kaufman’s case) when you start looking for explanatory power.

The PCs are ordered according to their contribution to the variance of the “x” variable. But if you’re regressing on them, you’re really interested in whether or not they explain variance in the “y” variable, and there’s no reason to assume these contributions will be the same.

In the usual regression case, there is one “y” to be explained, and several explanatory “x’s”. However, in the case of multiproxy calibration, there is only one explanatory “x” (temperature), and several y’s (proxies) to be explained. But whether there are more x’s than observations or more y’s than observations, there is no way to confirm that they are collectively significant without distilling them down to a handful of PC’s.

My point was that in either case, you can’t freely cherry-pick PC’s by including the ones that are significant and just pretending the others don’t exist, any more than you can do this with raw variables. Testing whether the first k (as ranked by singular value) are collectively significant imposes some discipline on this procedure, even if only number k jumps out as significant.

This may occur, but then it is not clear what function PCA is serving. Why not just use the raw X matrix directly?

You can’t use X directly because of multicollinearity. PCA orthogonalises the explanatory variables.

My point was that in either case, you can’t freely cherry-pick PC’s by including the ones that are significant and just pretending the others don’t exist, any more than you can do this with raw variables.

If it’s done wrong, it’s called “cherry picking”, but if you do it right it’s called “model selection”. Difficult, but not impossible.

I note we’re having som discussion here about how to decide whether particular trees are good thermometers. We’ve had lots of discussion about that in the past, but one important thing to bring up is the quality of the information availaable about the particular tree. Things like elevation, location on a mountain, soil depth or quality, etc. These kind of things will go a long way in deciding whether a given tree should be acceptable or not. You still should have a priori criteria but failure to have the proper info and / or use it should bring a data set into question.

Promoters of “obstruction” techniques to prove their case for the AGW debate have given the ammunition for the AGW skeptics to use the same approaches to “prove” the case against AGW. Be careful of what you say. I hope one day soon the debate is resolved so we can move on. As hinted by so many posters here, I also expect all researches apply the true meaning of the scientific method to their work. Sadly, it appears this is not the case for whatever reason. I doubt this is only a recent practice.

As a grad, my employer was engaged to conduct a study that was required to recommend the reduction of full time firemen at a rural fire brigade location which was staffed by both paid full time personnel and unpaid volunteers. I was tasked with collecting the data on incidents and personnel usage which appeared to me to show they were correctly manned and my draft analysis supported by graphs and tables reflected that.

Because the data did not support the required conclusion, when published, I found my data amended to suit the required conclusion. i.e. to show ‘false alarms’ as an incident requiring zero personnel even though several attended, ‘cat up a tree’ type grandma assistance callouts marked as 1 incident with 1 fireman (even if two or more attended), some minor fires that had gone out changed to 1 incident, zero personnel required etc. The real fires when they required maximum personnel were relegated to have little impact on the results by inventively maxing out the number of incidents.

In a nutshell, simplifying the analysis, the guy I worked for essentially changed the data to minimise the numerator and maximise the denominator by utilising various assumptions which were hidden in the text or not stated at all. In the end, the conclusion inevitably read that they were overmanned and x number of personnel could be replaced with unpaid volunteer staff.

Re: Steve McIntyre (#42),
Dear Steve, Lonnie Thompson was profiled on an episode of “NOVA scienceNOW” (that’s how they spell it) that airs on the PBS channel here in the USA. Good human story; seems like a very nice man; he’s from Huntington, West Virginia, just like my father is too; but the insightful part for me regarding the data is he is portrayed in the piece as the pioneer /rebel/ against the odds kind of scientist who gathers important ice core samples like nobody else; with very important data. (at least that’s my impression) CA readers might find the show insightful.

Here is what says in the synopsis: “Profile—Lonnie Thompson
A recent winner of the prestigious National Medal of Science, Thompson has been drilling ice cores at high elevations in the tropics since 1976. Why the tropics? Many fellow scientists were skeptical until Thompson showed that such cores preserve a detailed, millennia-old record of climate shifts in the most populous regions of the world.”here

You mean Lonnie showed the drilling samples that conveniently fit his theory and the ones that didn’t, did not see the light of day. Wow who knew science was this easy? Eureka I think I know how to cure cancer.

Re: welikerocks (#46), The comment’s not out of line so much as it is simply irrelevant. It doesn’t matter if he’s a nice guy who works hard. What matters is that his some of his conduct (regardless of motive) is an impediment to science.

You can’t use X directly because of multicollinearity. PCA orthogonalises the explanatory variables.

Orthogonalizing the regressors merely changes the basis for the space spanned by the regressors. OLS picks the same point from this space, and you get exactly the same forecasts, R2 and regression F test for the collective significance of the regressors.

The only difference is that with the raw X, you can point to the coefficients for Yamal, Tiljander, etc, and think about what they mean, while if you change to an artificial orthogonalized basis, this information is obscured.

Unless, that is, you want to use PCA to create a hierarchy of variables so that you can keep a manageable number that are collectively significant and discard the rest. This “empirical model selection” distorts test sizes a little, but not by nearly as much as just cherry-picking big t-stats from the full set of candidates. As you put it,

If it’s done wrong, it’s called “cherry picking”, but if you do it right it’s called “model selection”. Difficult, but not impossible.

So, with all due respect to Jolliffe, it seems to me that if you’re going to do PCA, you should definitely pay attention to the order of the PC’s. Beyond some threshold (say sqrt(sample size), or Preisendorfer’s Rule N), perhaps you should even ignore them altogether.

I have a post pending on Calibration in Kaufman. Perhaps we can discuss these matters at greater length there when it appears.

Orthogonalizing the regressors merely changes the basis for the space spanned by the regressors. OLS picks the same point from this space, and you get exactly the same forecasts, R2 and regression F test for the collective significance of the regressors.

Mathematically yes, but in practice the nearly-singular matrix will give you numerical problems.

If we get a good climatic story from a chronology, we write a paper using it. That is our funded mission.

It just struck me reading that. That reads more like the mission of a publishing house than a scientific team. There’s something intangibly just plain wrong about the way he chose to express that. It’s almost like he’s talking about a sci-fi novel.

Jacoby speaks of both quality data and good data. I believe that most people would agree that good data is of high quality.

Jacoby defines what he means by “good data”

If we get a good climatic story from a chronology, we write a paper using it.

He goes to say that he evaluates the quality of the data:

The quality can be evaluated at various steps in the development process. As we are mission oriented, we do not waste time on further analyses if it is apparent that the resulting chronology would be of inferior quality.

It appears to me that Jacoby is definining data of inferior quality to be that which does not provide a good climatic story. It sadens me that Jacoby does not find fault with his reasoning.